This manuscript represents an interesting and fundamental contribution, being the first attempt to apply a quantitative analysis to the shape of pavement cells across the whole diversity of vascular plants. The collection effort of the shape data is remarkable, and the recognition of the importance of taking phylogeny into consideration is highly commendable.
Given the importance that this contribution will indubitably have in stimulating the quantitative study of shapes in plants, there are a few points that a final version of this manuscript should deal with in my opinion.
First, the literature included in the introduction and the discussion is slightly biased towards the recent literature on the molecular mechanisms generating sinuous cell walls. However, this peculiar morphology, its distribution in different plant groups, and its relationship with different growth environments has interested botanists since the very early days of plant anatomy, as recognised in the introduction. A good summary of the older literature was conducted by Watson (1942), which is cited and referenced for the resemblance between some of the observation reported and the results presented. It would be nice if the authors included a more detailed discussion of the observations and hypothesis reported by Watson (1942) as well as other historical research in this field (for example, Volume I of Metcalfe & Chalk Anatomy of the Dicotyledons includes a nice discussion on pavement cell undulations and their distribution). This could help to make the current manuscript the new fundamental reference in this field of study.
A more important point regards the taxon sampling used for this study. If the 278 different species of vascular plants sampled represents a big improvement from a model species approach, this still represents less than one thousandth of all vascular plants species. Given this very limited sampling, a more detailed justification of the taxa chosen should be included in the main text. For example, it would be extremely good to include a distribution of species sampled by biome, habit, phylogenetic placement, as a main text table or as a paragraph in the text. In case of biases in the sampling, for example towards taxa from open biomes or particular clades of the eudicots, this should be acknowledged by the authors and discussed in the text. An oversampling of species from open habitats would in theory bias towards less undulating margin, according to the idea that such cells are associated with larger, shade leaves. This limited sampling also influence the strength of the conclusion of the article. The rarity of strongly undulating cells could represent a real pattern, but the data would support it only in case of a sampling proportional to clade richness. Moreover, it has been known that taxon sampling has a strong influence on phylogenetic comparative methods (for an example regarding the study of character correlation, see Ackerly, D. D. 2000. Taxon sampling, correlated evolution, and independent contrasts. Evolution, 54(5), 1480-1492) and this should be acknowledged as a limitation of the methods used here. Of course, the inclusion of a higher number of taxa would be nice, and could also be obtained by segmentation of images taken from the literature. However, I understand this is extremely labor intensive, and the manuscript with its current sampling represents a good starting point. As a small note, have the authors thought of employing confocal microscopy on PS-PI stained leaves? This could make automatic segmentation possible, especially if samples are first cleared using SDS.
Regarding the choice of the descriptors, have the authors tried to use the PCA scores in their analysis? It seems to me that using PC1 as a combined solidity-circularity estimator and PC2 as a mostly aspect-ratio influenced value could represent a valid alternative to just choosing two of the descriptors.
Another minor methodological point lies in the use of the Zanne et al (2014) phylogeny for the analyses. Especially for analyses of single clades (ferns, gymnosperms), more robust and well sampled phylogenies are available (for ferns, Lehtonen S, et al. 2017 Environmentally driven extinction and opportunistic origination explain fern diversification patterns. Scientific reports 7(1):4831), and could be used instead of the Zanne et al (2014) phylogeny, which is focused on the angiosperms. The phylogenetic methods employed are a bit unusual. The metrics most commonly employed for estimating phylogenetic signal in continuous traits are Pagel’s Lambda (Pagel 1999. Inferring the historical patterns of biological evolution. Nature 401:877–884.) and Blomberg’s K (Blomberg, S. P., Garland, T., & Ives, A. R. 2003. Testing for phylogenetic signal in comparative data: behavioral traits are more labile. Evolution, 57(4), 717-745.), and would be nice to see the authors employ this together with Moran’s I. This can be easily achieved for example using the function phylosig in the R package phytools. Moreover, it is unclear whether the correlations presented (for example in Figure 4 or Figure S2) represent simple linear regression or include a phylogenetic correction. It would be nice if the authors used a phylogenetic correction in their regressions.
There are only a few imprecisions in the language that might be corrected: for example, the authors refer to the ANA grade as a clade in line 238 (maybe use the word “group” if you want to include clades and grades together). They also refer many times to the “core monocots”: does this mean all monocots except Alismatales and Acorales? If “core eudicots” is a widely used, informal name for the clade of eudicots excluding Ranunculales, Trochodendrales, Proteales, and Buxales, “core monocots” it’s much less used and of less clear definition.
I hope that these comments will be useful for the authors to improve this manuscript. I am looking forward to its official publication and the impact it will have on the study of the evolution of morphology.